The Trouble With Physics

I’ve just finished reading Lee Smolin’s new book The Trouble With Physics, which should be released and available for sale very soon. It’s a great book, covering some of the same ground as mine, but with significant differences.

This won’t be a usual sort of review, since I’ll mainly concentrate on discussing the parts of Smolin’s book that I found most interesting, and my perspective here is kind of unique, having spent a lot of time writing about many of the same subjects that he covers. I will offer some capsule consumer advice: if you have any interest at all in what is going on these days in fundamental physics, you should buy and read both books. If you really are on a tight budget, and your main interest is in the relation of mathematics and physics, you should get mine. If your main interest is in quantum gravity or the foundations of quantum mechanics, you should get Smolin’s. His is more appropriate for someone with little background in this area, mine contains some significantly more demanding material which requires some expertise to appreciate.

What most fascinated me about Smolin’s book is the personal story behind it. He was a graduate student at Harvard during the same years that I was an undergraduate there, and describes well that place and time. The standard model had just been formulated a few years earlier, and experimental confirmation was pouring in. Many of the people responsible for the standard model were there at Harvard, and there was more than a bit of justifiable pride and arrogance. Smolin was of a philosophical bent, and initially put off:

The atmosphere was not philosophical; it was harsh and aggressive, dominated by people who were brash, cocky, confident, and in some cases insulting to people who disagreed with them.

He studied the philosophy of science and was very struck by Paul Feyerabend’s Against Method (there are also has some amusing tales of later personal encounters with Feyerabend). Feyerabend’s philosophy of science has been described as “anarchistic”; he sees no one “scientific method”, but science as a very human activity, in which all sorts of different tactics are used to make progress towards better understanding. Smolin recognized that much as he would prefer a more deeply philosophical approach, it was the much more pragmatic tactics of people like Coleman, Glashow and Weinberg, who wouldn’t be caught dead talking about the nature of space and time, or foundational problems of quantum mechanics, that was what was really having success.

Smolin begins his book by explaining what he (and I) see as the most important fact about the past thirty years of theoretical particle physics research. We’re in a historically unprecedented situation, with virtually no progress being made on the fundamental problems of particle physics for a very long time, despite huge efforts. In his description, the field has “hit a wall”; I like to describe it as a victim of its own success. The standard model is just too good. It’s too hard to find an experimental result that disagrees with it, and too hard to come up with theoretical advances that will address some of the things it leaves unexplained. Smolin sees the source of the problem in the field’s insistence on sticking with a way of doing science which worked until 30 years ago, but now has become dysfunctional, with string theory only a symptom of the underlying problem. He writes:

I have mentored several talented young people through crises very similar to my own. But I cannot tell them what I told my younger self – that the dominant style was so dramatically successful that it must be respected and accomodated. Now I have to agree with my younger colleagues that the dominant style is not succeeding.

Elsewhere he writes:

My hypothesis is that what’s wrong with string theory is the fact that it was developed using the elementary-particle-physics style of research, which is ill-suited to the discovery of new theoretical frameworks… This competitive, fashion-driven style worked when it was fueled by experimental discoveries but failed when there was nothing driving fashion but the views and tastes of a few prominent individuals.

Smolin was a student of Stanley Deser’s, and during his graduate student years supergravity was a field that was just taking off. He describes getting to know Peter van Nieuwenhuizen and Martin Rocek and being offered a chance to get into the field at the ground floor, one he passed up because he couldn’t believe that the kind of lengthy algebraic calculations they were doing could give real insight:

It was like being offered one of the first jobs at Microsoft or Google. Rocek, van Niewuwenhuizen, and many of those I met through them have made brilliant careers out of supersymmetry and supergravity. I’m sure that from their point of view, I acted like a fool and blew a brilliant opportunity.

Smolin didn’t join the Stony Brook supergravity group, but found that he could make a place for himself in the physics community working on quantum gravity, but using particle physicist’s methods:

… an easy opportunity opened up while I was a graduate student, which was to attack the problem of quantum gravity using recent methods developed to study the standard model. So I dould pretend to be a normal-science kind of physicist and train as a particle physicist. I then took what I learned and applied it to quantum gravity.

Smolin ended up with a post-doc at the new ITP in Santa Barbara, which luckily was running a program on quantum gravity that year. His career tactic almost didn’t pay off:

One day, as we were waiting for the results of our applications, a friend came by to tell me that I was unlikely to get any jobs, because it was impossible to compare me with other people. If I wanted a career, I had to stop working on my own ideas and work on what other people were doing, because only then could they rank me against my peers.

The most powerful parts of the book are the chapters entitled How Do You Fight Sociology?, and How Science Really Works. They give a detailed and clear diagnosis of the problematic way string theory research is being conducted, and decisions are being made about who deserves a job. Smolin has an insider’s point of view, particularly because he himself worked on string theory:

… during the years I worked on string theory, I cared very much what the leaders of the community thought of my work. Just like an adolescent, I wanted to be accepted by those who were the most influential in my little circle. If I didn’t actually take their advice and devote my life to the theory, it’s only because I have a stubborn streak that usually wins out in these situations. For me, this is not an issue of “us” versus “them,” or a struggle between two communities for dominance. These are very personal problems which I have been contending with internally for as long as I have been a scientist.

So I sympathize strongly with the plight of string theorists, who want both to be good scientists and to have the approval of the powerful people in their field. I understand the difficulty of thinking clearly and independently when acceptance in your community requires belief in a complicated set of ideas that you don’t know how to prove yourself. This is a trap it took me years to think my way out of.

Smolin gives many examples of the “groupthink” behavior of the string theory community, while characterizing string theorists as “almost all more open-minded and self-critical and less dogmatic than they are en masse.” He describes string theorists as:

… supremely confident both of the truth of string theory and of their superiority over those unable or unwilling to do it. To many string theorists, especially the young ones with no memory of physics before their time, it is incomprehensible that a talented physicist, given the chance, would choose to be anything but a string theorist.

…Anyone who hangs out with string theorists encounters this kind of supreme confidence regularly. No matter what the problem under discussion, the one option that never comes up (unless introduced by an outsider) is that the theory might simply be wrong. If the discussion veers to the fact that string theory predicts a landscape and hence makes no predictions, some string theorists will rhapsodize about changing the definition of science.

Some string theorists prefer to believe that string theory is too arcane to be understood by human beings, rather than consider the possibility that it might just be wrong.

Smolin finds in the string theory community a sense of entitlement and disdain for anyone who works on alternatives to the theory, with major string theory conferences never inviting people who work on alternatives to speak. An editor from Cambridge University Press told him that one string theorist said he would never consider publishing with the press because it had put out a book on LQG (I see why their publishing my book was out of the question…). At string theory conferences Smolin would be asked “what are you doing here?” or told “It’s so nice to see you here! We’ve been worried about you.” Some friends explained to him that if he wanted to be considered part of the string theory community he had to work not just on string theory, but on the particular string theory problems that were fashionable at the moment.

One problem for physicists trying to get tenured positions that Smolin mentions is that most universities now require letters from 10-15 people evaluating their work, with a small number of negative evaluations sufficient to sink their chances. If you’re working on something other than a mainstream topic, finding 10-15 people who can comment knowledgeably on your work can be impossible. He describes string theorists as mostly submitting the same two or three research proposals. This narrow concentration on a small number of problems is defended by some senior theorists as a “disciplined” approach, one that will more surely lead to progress than encouraging people to pursue a variety of different research directions.

Very recently, Smolin sees things changing:

Until last year I had hardly ever encountered an expression of doubt from a string theorist. Now I sometimes hear from young people that there is a “crisis” in string theory. “We have lost our leaders,” some of them will say. “Before this, it was always clear what the hot direction was, what people should be working on. Now there’s no real guidance,” or (to each other, nervously) “Is it true that Witten is no longer doing string theory?”

One can quantify this new situation by noting that there have been virtually no heavily cited new papers during the past few years, except perhaps for the KKLT one that is part of the landscape story.

Smolin notes that many string theorists (including himself) have often been ill-informed about the exact state of knowledge concerning crucial conjectures about string theory. One example he discusses in detail is that of the finiteness of multi-loop string amplitudes. The state of the subject is that one knows how to precisely formulate them and can show lack of divergences only up to two loops (this is due to the work of d’Hoker and Phong). At higher genus d’Hoker and Phong have a conjectural definition, but have not yet been able to show that divergences cancel. Few string theorists seem to be aware of this, and some of them react with great hostility and shower with insults anyone who mentions this issue (as I’ve done here on this blog).

There’s much else of interest in Smolin’s book, including a lot of material about what he sees as promising ideas in quantum gravity, discussion of research on the foundations of quantum mechanics, and a chapter on “seers”, people doing original work on foundations. These include ‘t Hooft, Penrose, and many others less well-known.

While I agree with just about all of what Smolin has to say about string theory, my own background is different and I see promise in very different lines of research than he does. I’m much more skeptical than him about our ability to get useful experimental data on quantum gravity, and see questions about quantum mechanics rather differently. My prejudice is that, lacking experimental guidance, the thing to do is to try and better understand the mathematical structures underlying the standard model. In the past, better physical models have gone hand in hand with deeper mathematics, and I’ll bet this will continue to be true in the future. Quantum mechanics has deep connections to representation theory, a part of mathematics that unifies many different subfields. It seems likely to me that a better understanding of quantum mechanics will come from better understanding representation theory and its connections to physics.

There’s a lot of other sorts of material in the book that I haven’t discussed, and I strongly recommend that people read the whole thing. It’s very, very good, and anyone interested enough to follow this blog will find it highly rewarding.

92 Responses to The Trouble With Physics

Anyone who hangs out with string theorists encounters this kind of supreme confidence regularly. No matter what the problem under discussion, the one option that never comes up (unless introduced by an outsider) is that the theory might simply be wrong.

I can’t say I know every young person in the field, but I’ve talked to a fair fraction, and I have to say that with a few notable exceptions, I don’t see that sort of dogmaticism anywhere. Saying that string theory might be wrong isn’t a particularly interesting observation, so I can see why it doesn’t come up, but I’ve rarely met someone who doesn’t think that string theory could be the wrong theory of quantum gravity.

Peter paraphrases Smolin as saying, “being offered a chance to get into the field(SUGRA) at the ground floor, one he passed up because he couldn’t believe that the kind of lengthy algebraic calculations they were doing could give real insight”…

Einstein would agree whole-heartedly with Smolin’s reluctance, and this goes to the heart of the problem in theoretical physics in my opinion. In the absence of experimental evidence for SUSY and/or a driving paradigm, string theorists have chosen to hack their way thru the jungle with a `mathematics machete’, obscuring any hope of real physical insight, and venturing off into the surreal world of mathematical physics, which with few exceptions, has seldom yielded any deeper insight into nature’s secrets.
Now, we are paying dearly for this obsession with math, with no end in sight. Only the LHC can level the playing field, as the recent astro-observations of Dark Matter did with the alt.theories of DM, MOND & TeVeS, which are now history.

Stefan, see http://www.math.columbia.edu/~woit/repthy.html for general background course on relevant maths and see http://arxiv.org/abs/hep-th/0206135 for some specific physical ideas explaining the Standard Model tentatively using such ideas. At top of page 51, the Standard Model particles are obtained with electroweak symmetry properties. This should be impressive if you are interested in the links between Standard Model and advanced mathematics without resorting to extra dimensions.

The taste in ideas for extreme abstraction in particle physics is set by symmetry principles more recently, and laws of nature further in the past. This is not the same approach that you use if you are dealing with relatively simple phenomena where you might try to guess a full mechanism and write down the relevant basic equations straight off, and then solve those equations.

If you take nuclear physics, where you have the shell model and the liquid drop model of the nucleus, you can use visual analogies to help formulate a model that makes checkable predictions, which are semi-classical. But with particle physics, it looks more promising to search for symmetry principles and other abstract laws than to guess a sem-classical model.

I mean, suppose you were crazy and guessed that the particle is like a piece of string, and then you found that to get it to work just as an ad hoc model you needed to make make it extra dimensional string, and then you still failed to predict anything with it for 20 years? How embarrassing!

From your semi-review I do not understand what is the main point of the book (I do not have it).
In my opinion The Trouble with Quantum Gravity is that it is disconnected from experiments: sociological difficulties are not the problem, but a consequence of it.

The Trouble with High Energy Physics is different: experiments have not told us what we hoped, and we are waiting for the verdict from LHC. So, better to discuss after LHC.

I had one more question. What kind of impact has string theory had on modern mathematics? I have lately been becoming more and more impressed with the number of branches of mathematics that have been impacted by string theory.

A sidenote : Feyerabend emphasized on the sociological aspect of science, but more : he saw scientific truth as a sociological phenomenon. In this respect the situation in today’s physics clearly disproves Feyerabend’s views since string theory is by no way acknowledged as a scientific truth, despite the sociological dominance of string theorists.

A question : does anyone know about another historical example of the “groupthink” Smolin describes ? I can think of the “N-rays” affair but it did not went that far, no lasted for so long.

Thanks for that Peter, I look forward to this book. I get impatient with Smolin because he’s such a nice guy, and it seems to me what physics needs is some “tough love” and a few bitch slaps now and then – but it’s obvious he is a sincere researcher and representative of all that’s good in science.

For contrast, one should poke over to Motl’s blog and read the page upon page of incoherent, basless ranting there. It’s mind boggling.

The LHC can’t contradict string theory, since string theory predicts nothing about what it will see. If the LHC sees something new and exciting, most theorists will be trying to figure that out, paying less attention to string theory.

The question of the impact on math of string theory is complicated. I did write something about this in my book, although that only scratched the surface. One complication is that much of the most important math that has come out of string theory research is really results from 2d QFT calculations.

Thanks for the links. I’m having a look through the Rep Thry paper; seems quite interesting. Do you know of any (introductory) texts you think are worth studying to get up to speed in this area?

Peter,

If you recall our discussions some time before, i.e. on gauge fields and Dirac operators, I have been combing through Amazon.com for relevant introductory texts. The best ones I could find were:

“An Introduction to Dirac Operators on Manifolds” — Jan Cnops

and

“Operator Methods in Quantum Mechanics” — Martin Schechter

If you have any added suggestions please let me know.

Among the ideas you place forward, studying “geometric quantization” holds, atleast from my neophyte vantage point, (potentially) fundamental insights into QM and QFT, and may even (with the passage of time and careful consideration) displace string theory as the most important approach to fundamental physics research… I do think IT’S THAT IMPORTANT!
I also wonder if von Neumann’s QM work would be helpful to study here? Do you also feel Jouko Mickelsson’s work is important enough for the afore-mentioned programme to warrant careful study? [No offence intended to the author, but the book’s cost is WAY too high for your average student to afford… unless it’s worth all my three months’ summer savings. ;-)]

I’d like to thank Michael Bacon for the link to the Smolin-Greene interview. Having listened to the interview now, I’d like to post my thoughts on it as a layman to the subject whose academic life has only been tangentially touched by string theory. I, like many other mathematicians (I presume) have no vested interest in whether strings are bogus or not — I’d just like to know some arguments in both directions, just for my general scientific edification.

Frankly, Michael Greene was far more polished (understandably, he’s had practice) and presented a more compelling point of view on general grounds. Smolin, in my opinion, was at times longwinded in his presentation, which hurt his debate.

Smolin has a difficult task to begin with. People, and scientists aren’t really interested in unclear claims about what doesn’t work, or “negative campaigning”. Smolin stresses the lack of experiments. Greene says things take time. (What’s wrong with that?) Moreover Greene asserts the mathematical consistency of things, which not knowing the specifics, sounds like reasonable evidence. These are things, Greene says, keep people inspired.

Smolin asserts that string people are holding back non-string people. He seems embarassed to make this claim directly, but rather hints at it in various ways. Greene counters that his _own_ graduate students sometimes work on non-string physics. Personally, I don’t find it surprising that one field in a subject looks down at other fields, or consumes resources. It’s annoying to be on the wrong side of the tracks, I know, but a priori, I have to admit this doesn’t mean to me that the ideas in the field per se are faulty.

So I summarize that string theory is an with high degree of mathematical consistency but which clearly needs experimentation. Its difficult math and difficult physics, so therefore time is necessary to come to an appropriate conclusion.

Is there something I’m missing? I’d be glad to be better informed on this debate…

Both my books and Smolin’s contain very detailed answers to your questions, I don’t want to try and rewrite a lot of this here. As for the Smolin-Greene radio show, it’s really not possible to sensibly debate these issues in a few minute long radio program for the general public. About all you can get off in that time are quick sound bites which will be highly misleading in one way or another. The quick answer to tg’s summary is that:

1. string theory does not have a high degree of mathematical consistency, actually no one knows exactly what the theory is.

2. the problem with string theory is not that it needs experimentation. The problem is that it can’t predict anything, at any energy, including being unable to retrodict things being studied in current particle physics experiments.

3. the theory is more than 30 years old, has been intensively studied for 22 years, with the result that it now looks a lot less likely you can get physics out of it than people thought 22 years ago. The problem is not that progress is slow, it is that progress is negative.

I don’t know the books you mention. One nice short introductory text on representation theory is Graeme Segal’s lectures in Carter, Segal, McDonald, Lectures on Lie groups and Lie algebras.
Unfortunately I don’t know a really good introduction to geometric quantization, in its relation to representation theory. There is a recent book by Kirillov, called “Lectures on the orbit method”, which may be the closest thing.

Saying that string theory might be wrong isn’t a particularly interesting observation, so I can see why it doesn’t come up, but I’ve rarely met someone who doesn’t think that string theory could be the wrong theory of quantum gravity.

This observation of yours, however, sounds particularly interesting! If it never comes up how can you be so sure that you never met anyone who thinks it is an impossibility, I mean, that String Theory could simply be wrong? Telepathy? Groupthink? Pray let us know…

The title of the book refers to what’s wrong with physics. The failure to recognize string theory’s shortcomings, because of its dominance, no matter how disturbing to skeptics, and no matter how unfair to competitors, is only a small part of the story of what’s wrong with physics.

On the Science Friday show, Smolin was just getting into the real problem, when Flato cut him off to take a call from a lady suggesting that what is needed is “thinking out of the box,” but before that he was addressing Green’s statement about the consistent calculations.

As Green explained how that extensive testing the consistency in the calculations of string theory, and its consistency with the established concepts of past physics, shows that the “theory comes through with flying colors every step of the way and keeps us thinking that things are at least headed in the right direction,” Flato turned to Smolin and asked, “Well, Lee, what would be wrong with that, if things are working like that?”

Smolin said:

If you really put quantum mechanics together with the description of space, then we know, from general considerations, that the notion of space should disappear. Just like the notion of the trajectory of a particle disappears in quantum mechanics, …the same thing should happen to space and the geometry of space.

I’m sure he was referring to background independence here, but he didn’t get to explain it very well, just that string theory doesn’t address this very directly, while other approaches do.

My question is, Peter, does he explains this well in the book, and does your work address this problem?

There’s a lot in Smolin’s book about the issue of background independence, not much in mine. In general I’m mostly writing about particle physics, Smolin is much more concerned with quantum gravity, and he certainly writes well and clearly. I don’t have any particular wisdom on this subject myself.

And please, if you want to discuss your favorite ideas about quantum gravity, don’t do it here.

I understand your reluctance to summarize complex arguments that you’ve already put years into expressing better elsewhere and I do promise that I will read your account in full when I get the opportunity.

At the moment though, I am a bit curious about whether the pro-string theory argument can summarized into the phrase: “The mathematical coincidences are too surprising to be chance.”

Could you say whether this is very, very roughly the crux of the pro-string theory argument?

The pro-string theory argument for unification is mainly that the theory provides a quantum theory of gravity.

The argument about mathematical coincidences is more that an argument that calculations show that things are happening in string theory for reasons that are not understood. This is just an argument that there is something going on in string theory that is not yet understood. That’s an argument for further research into the theory, but not an argument that it is going to give you a useful unified theory.

some mathemacians indeed say that string theory is an activity which produced some very beatiful and important mathematical ideas, which justifies this activity. Whether you want to call that activity ‘physics’ is another matter…

This observation of yours, however, sounds particularly interesting! If it never comes up how can you be so sure that you never met anyone who thinks it is an impossibility, I mean, that String Theory could simply be wrong? Telepathy? Groupthink? Pray let us know…

Conversations in social situations rather than in researchy situations.

I wouldn’t be surprised to see another “string theory” style sociological phenomena popping up decades later in particle physics, if string theory falls by the wayside in the near future. Seems like these sorts of things happen frequently enough every few generations or so.

Stefan,
I really liked Schechter’s book. You may be interested in some more recent work that follow’s Schechter’s. All of this can be downloaded from the following websites:
Barry Simon, Math Dept, Caltech
Gerald Teschl, Math Faculty, U of Vienna (both research articles and Lecture Notes [actually book preprints]),
Susanne Teschl, U. of Applied Sciences,Technikum Wien (thesis).
You can find all of these by using Google with the person’s name.
Best,
David

About the supreme confidence of string theorists – from the experience that I’ve had, it seems that there really are some amazing things that string theory has done. Counting rational curves is a good example; AdS/CFT and the dualities are impressive too, and it sure looks like it has something to do with quantum gravity, getting the entropy A/4 right for at least some black holes, and having Einstein’s equation in it and so on. These things are, quite frankly, too amazing to be just a coincidence.

The problem is that these things have been interpreted as evidence that string theory is the one true theory of the universe, but in fact it is evidence that there is some underlying self-consistent mathematical structure, which may or may not be a theory about physics. All of the signs seem to point towards the conclusion that it is not a theory about physics, but is rather a mathematical structure which relates 2d CFT to various gauge theories in various manifolds.

Still, though, the string theorists, like Ed Witten, like to oversimplify and say that they think string theory has produced too many fascinating insights to be “wrong”.

To Dan and Anonymous
I am one of those whose work was selected into top 12 results in string theory (e.g. read #6 in this list) mentioned by Dan and, indeed, I have to say that, for instance, work by Grisha Perelman would never be completed (most likely) should he in his 3 Fields medal winning papers not use some basic string-theoretic results obtained in 80ties. This fact alone is sufficient for justification of string theory existence. But, surely, I can mention many other things, e.g. read my hep-th/0608117 and references therein. Clearly, sooner or later the dust will precipitate and there will be a lots of good bits and pieces of work for grabs by everybody who likes to work more than to talk.

Because they had nothing to do with the posting, which is a review of Lee’s book. I’m tired of explaining this to people, but this is not sci.physics, it’s not a place for people to discuss their favorite ideas about physics. I don’t have the time, energy or interest to moderate something like that.

I’m pretty annoyed about this comment section today anyway, I’ve been spending a huge amount of time deleting comments from idiots who want to denounce Yau or Tian, using endlessly changing pseudonyms. I really, really don’t have time for this these days.

Egbert,
I noticed that typo and told the publisher about it. I’ve also set up my web-site so it responds properly to the incorrect URL.

Stefan and Peter,
When Stefan referred to Jouko Mickelsson’s work and a way to expensive book, I assumed that he meant Current algebras and groups, which AFAIK is the only book he has written. Since I have read (although perhaps not understood) both the book and the papers I linked to, I can claim that there is considerable overlap.

Your short review sure got me very interested in Smolin’s latest book! I have ordered both his and yours, and I am eagerly waiting to read them. hehe.. It’s very likely that I will be among a very few from my country, Mauritius, to read them (maybe Sanjaye Ramgoolam, a “string theorist” countrymate, at Queen Mary, will read one or both of them). Last time I tried convincing a friend about Physics, I ended up giving him Penrose’s “A Road to Reality” as birthday present!

Sorry, but I don’t even have an electronic form of the book, and couldn’t distribute it for free if I did. Anyone interested in acquiring the rights to publish a translation in another language needs to contact the people at Jonathan Cape, my deal with them was that they hold world-wide rights to publish the book.

Mathphys + tg,

The Science Friday show involved Brian Greene, not Michael Green. Brian is a lot better at this than Michael, I would think.

Peter, is it possible to state the main (say, 10-15) points for the “case against string theory” with 4-5 sentences on each?

This will be very helpful. Please consider doing it.

It will be useful to

a) separate the stricktly scientific points from more sociological and philosophical points

b) to separate points that say that (*)”string theory is not (yet) successful” from those saying that (**) “this and that aspects of the theory are fishy” from those saying that (***) “string theory is not the right direction for dealing with “final theory/grand unification”, from those saying that (***) “the whole endeavor of final theory/grand unification is misguided”.

c) To hint if physics requires more back-tracking or it is just string theory that is problematic.

dear Gina, I think that the main scientific problem is: since we cannot directly probe quantum gravity, a useful theory of quantum gravity must predict something at the lower energies where we can do experiments. Strings allow something like 10^500 different possibilities: this seems practically equivalent to allowing everything and predicting nothing.

I hope Peter will produce an introductory textbook on Representation Theory and Particle Physics.

Gina,

Your idea would I fear produce a list of string theory claims with the same boring label ‘uncheckable speculation’ beside each.

‘Extraordinary claims require extraordinary evidence.’ – Carl Sagan.

You can see plenty of extraordinary claims in string theory (it solves almost all the big problems of unification, quantum gravity, the nature of particles, black holes). You don’t see any stringy evidence, let alone extraordinary evidence, and nobody expects to find much.

The string theory failure has some weak precedents in science: check the detailed history in peer-reviewed physics journals on the “Vortex Atom” and “Aether” (both the subjects of intricate mathematical speculation and wild claims of ad hoc success from mathematical physicists including Kelvin and Maxwell, who both died firmly believing flawed theories).

However, string theory is more dangerous. At least Kelvin and Maxwell’s ideas could later be checked by experiment. String theory deliberately speculates about practically uncheckable phenomena (Planck scale unification, etc) so remaining safe from experimental refutation, so becoming a religion:

‘Whatever ceases to ascend, fails to preserve itself and enters upon its inevitable path of decay. It decays … by reason of the failure of the new forms to fertilise the perceptive achievements which constitute its past history.’ – Alfred North Whitehead, F.R.S., Sc.D., Religion in the Making, Cambridge University Press, 1927, p. 144.

At this point, I’m way too busy, and writing another explanation of what the problems are with string theory isn’t at all something I want to spend time on. The article I wrote back in 2001 is still a good short version of the argument, all it is missing is a discussion of how things have gotten much, much worse for string theory since then, because of the landscape.

The issues involved here are pretty complicated, and I don’t think short sound-bites, or me countering people’s “10 quick reasons why string theory is great” with “10 quick reasons why string theory doesn’t work” is going to be very enlightening. Partisans of one point of view or the other aren’t going to be convinced by this, and people who want to seriously understand the issues and make up their own minds should read both the pro-string theory point of view put forward in several books, and the other side of the story, as explained in my book and in Lee’s. I do believe that the problem is not just string theory, but more generally the idea of supersymmetric grand unification, these issues are discussed extensively in the book.

Lubos,
While, unlike you, I’m not banning those who disagree with me from posting comments here, I’m not going to tolerate and will continue to delete any comments like your last one that attack people other than me.